Measuring Treatment for Tax Policy Analysis. Caroline Weber* November Abstract

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1 Measuring Treatment for Tax Policy Analysis Caroline Weber* November 2014 Abstract This paper considers the conditions under which it is possible to obtain a particular intentto-treat (ITT) estimate the behavioral response to the tax change individuals would face based on their characteristics when the legislation was enacted and shows that this measure of treatment produces an estimate that is generally closer to the structural parameter of interest than the traditional measure. The bias associated with the traditional measure in the context of the elasticity of taxable income is substantively important; replacing the traditional with the ITT measure decreases the coefficient estimates by percent and the standard errors by percent. A special thanks to my dissertation committee for their invaluable encouragement and comments: Jim Hines, Joel Slemrod (Chair), Jeff Smith, and Kevin Stange. Also, many thanks to David Agrawal, Jon Bakija, David Cashin, Gigi Foster, Rob Garlick, Jacob Goldin, Laura Kawano, Wojciech Kopczuk, Jason Lindo, Andreas Peichl, Michael Smart, Sergio Urzúa, Glen Waddell, Michigan Tax Research Invitational participants, University of Michigan Public Finance Seminar participants, Urban Institute seminar participants, U.S. Department of Treasury seminar participants, American Economic Association meeting participants, Labour Econometrics Workshop participants, National Tax Association participants, International Institute of Public Finance Congress participants for helpful comments. All remaining errors are my own. This paper was previously circulated as The Fixed-Bracket Average Treatment Effect: A Constructive Alternative to LATE Analysis for Tax Policy. *Assistant Professor, Department of Economics, University of Oregon: cweber5@uoregon.edu. JEL Classifications: H21, H24. Keywords: elasticity of taxable income, tax policy analysis, optimization frictions, simulated instruments. 1

2 1 Introduction Empirical researchers frequently obtain estimates of the behavioral response to a tax change by exploiting variation in the degree to which a tax reform affects different groups of individuals based on their individual characteristics and tax situations. Often, the tax schedule examined has multiple brackets and at least part of the identification of the estimates comes from differences in legislated tax rate changes across brackets. Examples include examinations of the responses to the personal income tax schedule, the Earned Income Tax Credit (EITC), and social security contributions, among others. These estimates are important for policy analysis, both in terms of deadweight loss and revenue implications. In most contexts, a theoretical framework has been developed which maps from the estimates obtained to a calculation of deadweight loss. 2 In order for this mapping to be valid, the underlying structural parameter must be obtained, which can be more challenging to obtain than a simple estimate of the response to a particular policy change. Often, the empirical literature s key independent variable is the observed tax rate change an individual faced. The challenge of using the observed tax rate as an independent variable in an estimating equation is that we, as researchers, observe a tax rate for all individuals, but the tax rate we observe is systematically not the relevant tax rate for certain subgroups. This is because we only observe the tax rate the treatment after individuals have responded, and sometimes individuals face incentives to cross tax bracket lines (thereby altering their observed treatment) as part of their behavioral response. Additionally, the instruments we use for the observed tax rate change generally are simulated tax rate changes based on prereform characteristics. As a result, while the instrument is not correlated with endogenous selection, for a given treatment level, the treatment-instrument pair are often extremely informative about treatment mismeasurement. When this is true, the exclusion restriction is violated, albeit for a rather non-standard reason. 2 For example, Eissa et al. (2008) do this for the EITC, and Feldstein (1999) and Chetty (2009) do this for the elasticity of taxable income (ETI). 2

3 This is unlike a labor or other classic treatment effect setting in which there may be selection into treatment, but the treatment that determines individuals responses is observed, there is a random assignment mechanism before selection, and treatment based on random assignment is also observed. Because of these differences, the standard analysis and interpretation of the estimates obtained does not apply. The Local Average Treatment Effect (LATE) analysis proposed by Angrist and Imbens (1994), in particular, will never apply because instruments in this context will always violate either the exclusion restriction or monotonicity. This paper provides an appropriate set of assumptions and the resulting interpretation of the parameter obtained for this setting. This paper considers both the traditional way of defining a tax rate change when estimating the causal effect of a given tax policy the observed tax change an individual faces and a new measure the tax change an individual would face based on their characteristics at the time the legislation was enacted. For the former measure of treatment, we derive the conditions under which it is possible to obtain a causal average treatment effect (ATE) of a tax reform using pre-reform characteristics as instruments, taking treatment mismeasurement into consideration. We call the treatment effect obtained the Fixed-Bracket Average Treatment Effect (FBATE), which will identify the average treatment effect for individuals with no incentive to switch tax brackets in response to a tax reform or other shock that affects the tax bracket in which an individual is located. Similarly, we also consider the conditions under which we can derive an estimate based on the newly proposed measure of treatment, which produces a particular ITT estimate. We show that this estimate is often preferred to the FBATE estimate because a causal estimate can be obtained under weaker assumptions over a large subpopulation. Moreover, if the assumptions for FBATE are satisfied, for a given instrument, the ITT and FBATE estimates will converge. This analysis provides a standard which can be used to assess possible instruments and sources of identifying variation, interpret existing parameters, and identify conditions under which the response to future anticipated, as well as current, tax changes can be estimated. 3

4 Given these results, this paper then examines whether the ITT or FBATE estimates are preferred for obtaining a structural parameter in the context of the ETI. In the very important case of optimization errors, it is shown that the ITT method produces estimates that are closer to the structural parameter and the standard errors associated with this estimate are noticeably lower. In the special case in which the instrument is independent of all optimization errors, the FBATE estimate is also valid. In this special case, the ITT and FBATE estimates converge for a given instrument, and both identify the structural parameter. Finally, this paper empirically quantifies the difference in estimates and standard errors for the ITT and FBATE estimates in one particular setting estimating the ETI using the Tax Reform Act of This setting replicates estimates presented in Weber (2014), which can be interpreted as FBATE parameters if the necessary assumptions hold, and compares these to ITT estimates. We show that the estimates for broad and taxable income fall by 9.2 and 22.5 percent, respectively, when the ITT measure of treatment is used; while the differences are economically significant, they are not statistically significant. The standard errors are also remarkably lower when the ITT estimates are used; they fall by 13.8 percent for the taxable income estimates and 25 percent for the broad income estimates. The paper proceeds as follows. Section 2 lays out a framework for causal inference, explores the empirical challenges using the ETI as an example, and derives the conditions under which we can obtain FBATE and the corresponding ITT estimate in this context. Section 3 compares the ability of the ITT and FBATE estimates to reveal the underlying structural ETI parameter in various tax settings. Section 4 applies the results in this paper to an empirical example estimating the ETI using TRA86. Section 5 concludes. 4

5 2 Causal Inference for Policy Analysis In this section, we lay out a framework for causal inference for policy analysis. We will use the estimation of the ETI as our running example throughout this section; however, the analytics are written generally for any marginal or average tax rate change, and apply broadly to all cases in which researchers are trying to estimate the causal effect of a tax rate change when there are multiple tax brackets. Moreover, a substantial portion of this analysis also applies to all policy analysis with simulated instruments, which is discussed in Section 2.5. Section 2.1 focuses on casually exploring the challenges associated with estimating the causal effect of a marginal tax change using panel data and motivates Section 2.2. Section 2.2 derives the conditions under which an intent-to-treat (ITT) estimate and a causal average treatment effect (ATE) are obtained. The ITT estimate captures the behavioral response to the tax change an individual would face based on their characteristics at the time the legislation was enacted. A unique feature of this setting is that the causal ITT and ATE estimates often converge, and estimating a Wald estimate where the ITT estimate is rescaled by the observed tax rate change does not produce a causal ATE. We also show how to interpret these parameters. In Section 2.3, we extend the analysis to cases in which the tax rate is anticipated. In Section 2.4, we discuss how the results apply to repeated-cross-section data. 2.1 The Challenge Explored Consider the tax reform depicted in Figure 1. The x-axis in this figure is before-tax income (Y ) and the y-axis in this figure is after-tax income (Y T (Y )). There are two periods, period 1 and period 2. In period 1, a progressive tax schedule exists and is depicted by the solid green line. In period 2, the marginal tax rate increases for all individuals above 5

6 the tax kink k; the new budget set is depicted by the dashed yellow line. 3 The standard Figure 1: Tax Reform where Tax Rate Increases above k Y- T(Y) 1- τ 1 1- τ t2 1- τ c1 =1- τ c2 k Y difference-in-differences regression written down in the literature to obtain the parameter of interest, ε, is given by: 4 ln[yit] = α + ε ln[1 τit] + νit (1) where ln[y it ] is the change in taxable income, α is a constant, ln[1 τ it ] is the log marginal net-of-tax rate change, and ν it is the error term. The parameter of interest captures the percent change in taxable income due to a one percent change in the marginal net-of-tax rate the elasticity of taxable income (ETI). One of the main challenges presented by this estimating equation is the correlation between transitory income shocks ( ν it ) and the tax rate ( ln[1 τ it ]), but we ignore that for now by assuming there are no transitory income shocks or other secular income trends (e.g. income growth over time). We will come back to transitory income shocks and secular income trends later in this section and we can ignore 3 Note that if there was a tax decrease above k instead, some of the analysis presented here would be slightly different, as will be made clear in Subsection For the purposes of this section, we suppress all other covariates, including year fixed-effects, without loss of generality. 6

7 them for now without loss of generality for the concern we want to examine more closely. Sometimes individuals choose to cross tax bracket lines in response to the tax reform; for example, suppose someone decreases their income to below kink point k in response to the tax reform. For the purposes of this section, we are not concerned about the reasons behind this occurrence; a detailed discussion of this and its implications for the parameters discussed in this section is found in Section 3. Given that individuals sometimes cross tax bracket lines, it seems fairly obvious in the example depicted in Figure 1 that, in order to capture the tax change that individuals responded to, we want to define ln[1 τ it ] as the tax rate that occurs based on individuals period 1 income. So, ln[1 τ it ] would be negative for individuals above the tax kink in period 1 and would be zero for those below the tax kink in period 1. The fact that the increase in tax rate above k actually drove some individuals to a tax rate below k should be irrelevant for determining the relevant treatment these individuals face they should be considered as facing the tax rate increase just as anyone else who was above k in period 1 but responded in a less extreme way (and is thus still above k in period 2). While it may seem sensible, the definition of treatment described in the last paragraph is not the definition of treatment pursued in the ETI literature; ln[1 τ it ] is instead defined as the observed tax rate faced by the individual in each period. So, for example, individuals who begin above the tax kink before the tax reform and move below the tax kink in response to the reform would be assigned a positive value of ln[1 τ it ], even though they decreased their income in response to a negative value of ln[1 τ it ]. One can imagine that if there is no instrument for ln[1 τ it ] or the instrument is correlated with these individuals who face this treatment mismeasurement, the estimate will be biased. 5 To highlight the exact problem created by treatment mismeasurement, we now consider a 5 The problem is similar to the contamination bias discussed in Heckman and Robb (1985), in the sense that we do not observe treatment accurately for all, and if we assigned treatment in the most obvious, observable way, the estimates would be biased. It is very different from the large literature on imperfect compliance with experiments in which the relevant treatment after selection has taken place is observed and random assignment is not a function of pre-treatment characteristics. 7

8 common setting in which we think of the period 1 measure of treatment as an intent-to-treat (ITT) estimate based on individuals locations in the income distribution in period 1. The Wald estimate uses the ITT measure as an instrument for the observed tax rate change. While this setup may quickly seem like a straw man, this is actually the method used in the most frequently cited paper on the ETI (Gruber and Saez, 2002), making it a worthwhile example that also helps builds intuition. In order to exploit the potentially attractive quasi-natural experiment depicted in Figure 1 to estimate meaningful ITT and Wald estimates, we assume that the treatment and comparison groups look the same in the absence of a tax reform and will respond the same to a tax reform if they are treated. Given this assumption, we can estimate the causal average treatment effect ε as the difference in the change in taxable income between these two groups, scaled by the difference in the marginal net-of-tax rate tax change between these two groups: ε IT T = E [ ln(y (t1)) ln(y (c1))] E [ ln(1 τ(t1)) ln(1 τ(c1))], (2) where ln(y (t1)) is equal to ln(y ) multiplied by an indicator for being in the treatment group in period 1 and ln(y (c1)) is equal to ln(y ) multiplied by an indicator for being in the comparison group in period 1. The same applies for τ in the denominator. Note that ln(1 τ(c1)) = 0. This is an ITT estimate because the treatment and comparison groups are defined based on the intended tax rate change given their taxable income in period 1. From a policy perspective, this is a very meaningful parameter given where people are located when the government is deciding to change the tax rate, what happens? It may or may not be ideal for identifying the underlying structural parameter that tells us what would happen if things were a little different next time; for example, if individuals were more likely to overcome their optimization frictions in response to the next tax reform. We answer this question in Section 3. Now, suppose that we use the tax rate change based on period 1 income as an instrument Z for the observed tax rate change, such that Z = 1 if the individual was above the tax kink 8

9 in period 1 and 0 otherwise. We can write the Wald estimate as: 6 ε W ald = E [ ln(y (t1)) ln(y (c1))] E [ ln(1 τ) Z = 1] E [ ln(1 τ) Z = 0], (3) The numerator of ε W ald and ε IT T are the same, but the denominators are different. In particular, the denominator of ε W ald is smaller in absolute magnitude because E [ ln(1 τ) Z = 1] captures a tax rate increase for those that did not deviate below the tax kink, but captures a tax rate decrease for those that decreased their income below the tax kink in response to the tax reform and E [ ln(1 τ) Z = 0] is left unchanged. This can be shown more formally, by rewriting the denominator of ε W ald as: denom W ALD =denom IT T P [dd = 1 Z = 1] E [ ln(1 τ(t1))] + P [dd = 1 Z = 1] E [ ln(1 τ(dd))] (4) =denom IT T + P [dd = 1 Z = 1] E [ ln(1 τ(dd)) ln(1 τ(t1))] where dd = 1 if an individual chooses to deviate below the tax kink and zero otherwise and ln(1 τ(dd)) is the net-of-tax rate change for these individuals multiplied by the indicator variable dd. The absolute value of denom W ALD is always lower than absolute magnitude denom IT T, leading ε W ALD to overestimate the true effect of the tax change. The Wald measure of treatment would be fine if we used an instrument that was not correlated with the treatment mismeasurement. This unusual result that the Wald estimator does worse at revealing the population average treatment effect than the reduced-form ITT estimate is due to the fact that treatment is mismeasured and the Wald estimator is based on the assumption that the tax rate based on period 1 income is wrong and the observed tax change is right, not the other way around. In a more technical sense, what is the problem? The exclusion restriction is violated when Z is the accurate treatment and the observed tax change is wrong. This occurs because the 6 Note that E [ ln(y ) Z = 1] = E [ ln(y (t1))] and E [ ln(y ) Z = 0] = E [ ln(y (c1))]. 9

10 relevant measure of treatment is determined by Z, not the observed tax change, so Z will have a direct effect on the outcome. Given what has been uncovered in this section when there are no transitory income shocks, there appear to be two ways forward: (1) we could use the traditional measure of treatment the observed tax change but pick an instrument that is independent of the treatment mismeasurement documented in this section, or (2) define treatment as a function of period 1 income with no additional restrictions on the instrument. The next section will formalize this intuition, but first, we want to explore how this prescription is affected when transitory income shocks are re-introduced. When transitory income shocks are re-introduced, we cannot generally capture a meaningful behavioral response of individuals who face transitory income shocks or secular income trends that lead them to cross tax brackets. The movement across tax brackets is endogenous and what we want to capture is that some individuals faced a positive transitory income shock which moved them above k causing them to experience an increase in their marginal tax rate. In response, they want to re-adjust their income back below the tax kink by engaging in income smoothing across sources or time periods. Unfortunately, once they adjust their income back below the tax kink, it appears they faced no tax change, and we have no way of uncovering who would have faced a tax change before they adjusted their income in this setting. Therefore, we think of these individuals as being just as problematic as those who have treatment mismeasurement as described above. As a result, the introduction of transitory income shocks will play an important role in interpreting the parameters we obtain in the next section and will force us to have an instrument for both the ITT and ATE parameters, but will otherwise have very little effect on the points made in the paper thus far. 10

11 2.2 Obtaining and Interpreting a Causal ATE This section formalizes the intuition that we gained in the last subsection and derives an interpretation of the ITT and causal ATE parameters that we can obtain in this setting. First, we derive the ITT estimate. As in the last section, we will assume that the instrument Z is binary. This makes the notation more transparent without loss of generality. To derive the ITT estimate, we first divide individuals i into four principal strata (Frangakis and Rubin, 2002) based on two potential income indicators S i (1) and S i (2): 7 HH = {i S i (1) = S i (2) = 1}: individuals whose income is above k in period 1 and in period 2. HL = {i S i (1) = 1, S i (2) = 0}: individuals whose income is above k in period 1 and below k in period 2. LH = {i S i (1) = 0, S i (2) = 1}: individuals whose income is below k in period 1 and above k in period 2. LL = {i S i (2) = S i (1) = 0}: individuals whose income is below k in period 1 and in period 2. Period 1 and period 2 indicate income in period 1 and period 2, respectively, excluding any behavioral response to tax rate changes, where the tax changes were either legislated or induced by a transitory income shock or secular trends. 8 We now make some additional assumptions that are necessary to obtain a causal average effect for the ITT estimate of interest. Assumption 1: Let Z be a trivial function of each strata except HH and LL. 7 Wwe e define these groups assuming that the tax rate changes for those above k, which is the most common form of tax change; however, the results are equivalent if the groups are instead defined assuming that the tax rate changes below k. 8 Note that in the simple example used in this section where there is a single tax rate in period 1, whether the strata are defined as a function of period 1 or period 1 does not matter, but it will matter for more complex tax reforms, which are discussed later in this section. 11

12 Put another way, Assumption 1 assumes that the period 1 tax rate and Z are not correlated for groups of individuals who face transitory income shocks or secular income trends that change their marginal tax rates and thus provide these individuals with an incentive to change tax brackets. However, Z must be correlated with the period 1 tax rates for groups HH and LL; otherwise, we would have a weak instrument problem. Assumption 2: Let the difference in potential outcomes ln(y (HH)) ln(y (LL)) be the same, on average, for all individuals in strata HH or LL. Assumption 2 means that the treatment and comparison groups look the same in the absence of a tax reform and will respond the same to a tax reform if they are treated. This assumption is pervasive throughout the treatment effects literature. This assumption is actually stronger than necessary. ln(y (HH)) ln(y (LL)) can vary across individuals in these two groups, but this variation must be independent of Z. A popular alternative to Assumption 2 is monotonicity. 9 This restriction would generate a LATE-style parameter, but we do not focus on this restriction, because instruments used in this literature are either not monotonic or grossly violate Assumption 1. To make Assumption 2 hold in practice, the analysis is often restricted to individuals in a region around the tax kink. To introduce that restriction here, let all individuals in [k(1), k(1)] be included in the estimation, where [k(1), k(1)] are the thresholds [k, k] determined by period 1 income. Note that around k(1), some individuals who would be excluded except that they receive a negative transitory income shock in period 1 are included and some individuals who would be included except that they receive a positive transitory income shock are excluded. The reverse is true around k(1). For these cutoffs to not bias the estimates, the instruments must be independent of the selection induced in the outcome of interest by using these cutoffs. The next assumption, which among other things provides an instrument exogeneity condition, should make this necessary condition hold. 9 Monotonicity is the assumption used by Angrist and Imbens (1994) to obtain the Local Average Treatment Effect (LATE). 12

13 Assumption 3: Let the potential outcome ln(y ( )) and treatment status be jointly independent of Z for each principal stratum. Assumption 3 includes the standard instrument exogeneity condition, which has been a focal point of instrument selection in the tax reform treatment literature. 10 This also imposes the common assumption that the growth rate of income in the absence of the tax reform must be the same above and below the kink. 11 It also encompasses the exclusion restriction. Proposition 1: Given Assumptions 1, 2, and 3, the following ITT estimate is obtained from a Wald estimator, where treatment status is defined by period 1 income: ε IT T = E [ ln(y (HH)) ln(y (LL)) HH + LL = 1] E [ ln(1 τ(hh)) ln(1 τ(ll)) HH + LL = 1]. Proof: See Appendix. Recalling the discussion about the ITT estimate in the last section and comparing the parameter estimate shown there to the estimate derived in this section, they are the same when there are no transitory income shocks, and with transitory income shocks, here ε IT T identifies the ITT estimate over the subpopulation who does not face transitory income shocks that provide individuals with an incentive to cross tax bracket lines. Note that Assumption 1 is effectively a stronger form of the instrument exogeneity condition imposed by Assumption 3. We could alternatively drop Assumption 1, and replace it with a stronger form of Assumption 2 namely that individuals would respond to a tax change in the same way in all four strata. Assumption 3 would require the transitory income shocks and responses to these shocks to cancel out, so we would be left with a weighted average response to the legislated tax change across the treated strata. But, given the stronger form of Assumption 2 imposed, this estimated response is identical to the response defined in Proposition In reality, despite the literature s general concern with this condition, many instruments used violate this condition (Weber, 2014). 11 Alternatively, additional variables could be used to control for the heterogeneous growth rate. 12 Capturing a meaningful response to individuals responses to transitory income shocks or allowing individuals who face large transitory income shocks to respond in a different way that is reflected in the 13

14 Now, we consider the conditions under which we can obtain a causal average treatment effect when treatment is defined as the observed tax rate. To define the causal average treatment effect that can be obtained in this case, we again divide individuals i into four principal strata (Frangakis and Rubin, 2002) based on two potential income indicators S i(1) and S i(2), this time to capture incentives to deviate from both legislated tax rate changes as well as potential movement across tax brackets due to secular income trends and transitory income shocks: HH = {i S i(1) = S i(2) = 1}: individuals whose income is above k in period 1 and period 2 and who face no incentive to deviate below k when the tax rate changes. HL = {i S i(1) = 1, S i(2) = 0}: individuals whose income is above k in period 1 and period 2 and who face an incentive to deviate below k when the tax rate changes. Or, individuals whose income is above k in period 1 and below k in period 2. LH = {i S i(1) = 0, S i(2) = 1}: individuals whose income is below k in period 1 and period 2 and who face an incentive to deviate above k when the tax rate changes. Or, individuals whose income is below k in period 1 and above k in period 2. LL = {i S i(2) = S i(1) = 0}: individuals whose income is below k in period 1 and period 2 and who face no incentive to deviate above k when the tax rate changes. The term incentive to deviate refers to all individuals who may wish to deviate when the tax rate changes, whether or not they are, in fact, responsive enough to choose to deviate. Defining the groups based on their incentive to deviate rather than their actual deviation will enable me to define a parameter that will have substantially more policy relevance. The assumptions needed to obtain a causal average treatment effect in this case are identical to the assumptions needed for the derivation of the ITT parameter, where the measure of treatment and the relevant strata are changed: parameter estimates obtained is beyond the scope of this paper. 14

15 Assumption 1b: Let Z be a trivial function of each strata except HH and LL. Assumption 2b: Let the difference in potential outcomes ln(y (HH )) ln(y (LL )) be the same, on average, for all individuals in strata HH or LL. Assumption 3b: Let the potential outcome ln(y ( )) and treatment status be jointly independent of Z for each principal stratum. Note that parts of Assumptions 1b and 3b both address the exclusion restriction one way of interpreting this part of Assumption 1b is that it is defining how the exclusion restriction violation that generally exists in this setting will be resolved. Without a resolution, Assumption 3b is violated. Note, too, that while we can still consider exchanging Assumption 1b with a stronger version of Assumption 2b for the potential deviations due to transitory income shocks, the same is not true for potential deviations for other reasons; if we relaxed Assumption 1b for these individuals, too, Assumption 3b will be violated. Proposition 2: Given Assumptions 1b, 2b, and 3b, a Fixed-Bracket Average Treatment Effect (FBATE) is obtained from the Wald estimator and is given by: ε F BAT E = E [ ln(y (HH )) ln(y (LL )) HH + LL = 1] E [ ln(1 τ(hh )) ln(1 τ(ll )) HH + LL = 1]. Proof: See Appendix. We term this parameter the Fixed-Bracket Average Treatment Effect (FBATE), because it is the average treatment effect for individuals with no incentive to cross tax bracket lines in response to a tax reform or tax change brought about by a shock in taxable income or secular income trend (i.e. those in strata HH and LL). The assumptions required in order to obtain ε F BAT E are stronger than those required to obtain ε IT T, because for ε F BAT E, the instrument Z must be independent of all incentives to deviate, not just those associated with secular income trends and transitory income shocks. Because of this, ε IT T has the possibility 15

16 of identifying a causal effect effect for a larger subpopulation under weaker assumptions, than defining treatment based on period by period income. Corollary 1: When the assumptions for Propositions 1 and 2 hold simultaneously for a particular instrument Z, ε IT T = ε F BAT E. What is unusual about the ITT estimate defined in Proposition 1 is that when Corollary 1 holds, for the subpopulations over which ε IT T is identified strata HH and strata LL it is not an ITT estimate at all; rather it is a causal average treatment effect because for these individuals the intended and observed treatments are identical. Corollary 1 provides one way to test whether the additional assumptions necessary to obtain ε F BAT E hold. If ε F BAT E and ε IT T are statistically different for a given instrument Z and the assumptions necessary to obtain ε IT T hold, we can reject the null hypothesis that the additional assumptions needed to obtain ε F BAT E hold. Whether or not these parameters are relevant for tax policy analysis depends on the average treatment effect captured. When the potential outcomes split by the principal strata are homogeneous across all individuals, this parameter will be the relevant parameter for tax policy analysis. However, if there is heterogeneity in potential outcomes due to variations in underlying preferences, the elasticity estimates obtained are no longer guaranteed to be relevant for tax policy analysis. This is because FBATE does not reflect the response of those with an incentive to deviate who in this case respond differently to a change in their marginal tax rate relative to those who are not potential deviants. The discussion up to this point has assumed that there was a tax rate increase above kink point k in period 2. While this is sometimes accurate, there are also many tax reforms where there was a tax decrease instead of a tax increase, and there are also occasional examples where part of the tax schedule is regressive. Introducing these variations has no effect on Proposition 2 because these individuals appear in the comparison group in period 1, but are responding to the tax rate change in the treatment group (i.e., they are LH individuals). However, this does introduce additional treatment mismeasurement into tax change defined 16

17 as a function of period 1 income. Before the introduction of these variations, there were only individuals with incentives to deviate of type HL, but the relevant group for these individuals was the treated group, so period 1 treatment assignment was accurate. Leaving the strata for the ITT estimate defined as before will introduce a downward bias in the estimates if most of the mismeasurement occurs when Z = 0 and an upward bias otherwise. Alternatively, the strata can be revised to incorporate these incentives to deviate. This yields an average treatment effect for a subpopulation that is narrower than that originally found in Proposition 1 but still wider than that found by its analogue in Proposition 2. If the assumptions for Proposition 1 do not hold in this case, the bias induced by the treatment mismeasurement is strictly less in absolute magnitude for ε IT T than ε F BAT E. This section has focused on tax reforms as identifying the causal effect of a tax rate change. Other sources of changes in the tax schedule, such as bracket creep 13 or a change in the number of dependents 14 have been touted in the literature as having the following advantage:...one can compare taxpayers who are very similar both in income and initial marginal tax rate but yet face different prospects for changes in marginal tax rates and hence potentially make a much more convincing case for identification. The main drawback of this strategy is that taxpayers may not be aware of the minute details of the tax code...(saez et al., 2012). From the perspective of this paper, such an identification strategy is even more fundamentally problematic. For example, consider using bracket creep as identifying variation. Now, the observed tax change is not zero only when an individual moves across the tax bracket line. As a result, individuals who wish to shift their income across time periods to minimize their overall tax burden or those who do not wish to earn income in the next bracket due to their labor-leisure preferences are less likely to be observed as treated. 13 In the U.S., the personal income marginal tax rate schedule was fixed in nominal terms until Saez (2003) uses this source of variation to estimate the ETI during , which was a period of about 10 percent inflation. 14 This source of variation is used by Looney and Singhal (2006). They argue that the individuals they examine are likely not to respond to the future tax change before it is implemented. However, this identification remains similarly problematic to bracket creep unless individuals respond, but never by shifting their income below the tax bracket line, which obviously cannot be true. 17

18 This will create a substantial bias in the estimates unless the instrument is independent of these incentives to deviate. But, unfortunately almost everyone faces an incentive to deviate given the narrow window examined on either side of the tax kink, so no causal parameter can be identified. 2.3 A Causal ATE with Anticipation? Anticipated tax reforms have been ignored up to this point and are the focus of this subsection. We discuss the challenges faced when examining anticipated tax reforms assuming that the researcher has decided to estimate a separate parameter which captures the response to the anticipated tax change. The discussion in this subsection applies equally well to a tax reform that is anticipated and an anticipated change in the tax schedule due to something like the loss of a dependent. Except in the most ideal (and likely unrealistic) situations, the anticipation of the tax reform creates additional incentives to deviate; often these incentives to deviate apply to a large portion of the population being analyzed and likely make it impossible to estimate a causal FBATE parameter of the response to the anticipated tax change. As an example, consider again the tax reform depicted in Figure 1. Suppose in period 1 individuals with taxable income above k learn that their marginal tax rate will increase in period 2 due to a change in the tax schedule. Let the treatment effect of interest be the change in the outcome between period 0 and period 1 in response to the anticipated tax change that takes place between period 1 and period 2. There are now two parameters to estimate the response to today s tax change and the response to tomorrow s tax change. The true anticipated measure of treatment is non-zero either because there is an anticipated change in the legislated tax rate between period 1 and period 2 or because an individual receives a transitory income shock in period 1 or period 2 that makes the tax rate different across the two periods. The former identifies the parameter of interest in this subsection. As in Subsection 2.2, all individuals with an incentive to deviate either in response 18

19 to the anticipated or the contemporaneous tax rate change create a treatment mismeasurement problem. Additionally, all tax changes caused by transitory income shocks provide an incentive to deviate. Thus, the relevant strata are now HH, HL, LH and LL, where the membership in strata LH and HL now is also determined by incentives to deviate in response to anticipated legislated tax rate changes. If the same conditions are satisfied for these strata, Proposition 2 applies as before. The rest of this subsection focuses on who is now included in strata HL and LH. Given this, the feasibility of obtaining an FBATE estimate of the anticipated tax change is discussed. Let R be the amount of taxable income the individual reports in each period and SH be the amount of income that can be shifted across two periods. We assume SH > 0, because if SH = 0, the response to the anticipated tax change will be zero by construction, and thus not interesting to estimate. Consider individuals who are in the treatment group in both periods absent a tax reform. If these individuals decide to respond in period 1 to the legislated tax change in period 2 depicted in Figure 1, they will attempt to shift their income out of period 2 and into period 1 up to R = k. If they can shift smoothly (so no one shifts to R < k), then there is no incentive to deviate. However, if perfect smoothing is not possible, this creates an incentive to deviate. We don t have clear evidence on the degree to which perfect smoothing across periods is possible, but if evidence from the static context on optimization frictions, such as imperfect bunching, is any guide, imperfect smoothing exists. Unfortunately, this means that anytime there is an anticipated tax change, there is an incentive to deviate (at least within a reasonable region around the tax kink), and thus the parameter must be independent of all responses, which makes it impossible to obtain a causal average treatment effect using a period by period measure of treatment. Even if we assume perfect smoothing, more complicated tax reforms are problematic. 15 As an example, consider a case where there are only two tax brackets and the tax rate re- 15 This is somewhat in contrast to estimation of FBATE in the absence of anticipation, where a more complicated reform may introduce more chances to deviate, but does not eliminate the possibility of obtaining FBATE altogether. 19

20 mains fixed across periods, but the location of the tax kink moves from $60,000 in period 1 to $70,000 in period 2. Let permanent income, absent a tax reform, be $62,000. Individuals can minimize their tax liability across periods by shifting income into period 2 anywhere in the range $2,000-$8,000. Unless the individual chooses to shift exactly $2,000 this creates treatment mismeasurement; therefore, these individuals have an incentive to deviate. More generally, all individuals with permanent income levels between the old and new tax kink location who can shift their income to avoid the higher tax rate in either period face an incentive to deviate. Therefore, the instrument would need to be independent of all individuals in this region. With shifting income across periods, defining the anticipated treatment as a function of period 1 income instead will not reveal a causal ITT estimate either because treatment in period 1 is also often mismeasured (because individuals are shifting into or out of period 1). Instead, Proposition 1 would have to be applied to period 0 income for both the anticipated and contemporaneous tax changes. Depending on the application, this may increase the variance of the estimates too much to be feasible. 2.4 A Causal ATE with Repeated-Cross Sections Data The implications of Propositions 1 and 2 also apply to repeated cross-section analysis, because the treatment mismeasurement problem in period 2 that is analyzed here applies equally well to the repeated-cross-section context. The instrument must be uncorrelated with the outcomes of the same subpopulations in period 2 regardless of whether the data is panel or repeated-cross-section and a good repeated-cross-section instrument will capture the same subpopulations in both periods. Often, the most substantive concern with repeated cross-section analysis is a change in the composition of the treatment and comparison groups between period 1 and period 2. Proposition 2 highlights that if the instrument is chosen properly to address treatment mismeasurement, the composition bias is also eliminated; that is, in the repeated cross-section context, treatment mismeasurement and composition 20

21 bias manifest themselves amongst the same subpopulation and addressing the former also addresses the latter. Note that the choice of [k, k] to make Assumption 2b valid is particularly important in the repeated-cross-section context. Suppose, instead of imposing the cutoffs [k(1), k(1)] in both periods, the researcher defines individuals membership period by period, so that the restriction is still [k(1), k(1)] in period 1, but in period 2 it becomes [k(2), k(2)], as is common in the repeated-cross-sections context (and the only feasible cutoff if panel data are not available). No causal average treatment effect can be obtained in this context; in fact, with a uniform income distribution and a homogeneous response to the tax change, the estimated effect using this method will be zero individuals will flow in and out of the treatment group, but the average income of those within the group will not change. 2.5 Lessons for Other Policy Studies with Simulated Instruments The intuition of FBATE applies not only to tax policy, but also to all policy analysis using simulated instruments to address endogenous selection into treatment whenever the treatment due to endogenous selection has a different average effect on the outcome than treatment due to exogenous policy changes, which may often be the case for simulated policy instruments. The intuition expressed in these contexts, the tax literature included, seems to be that some of the measured treatments are relevant for the outcome and some are not; if we choose an instrument that is only a function of the relevant cases in which individuals were treated, we will obtain a causal ATE. This paper has shown that this intuition is false. To show what occurs in a non-tax context under various assumptions, we briefly consider Currie and Gruber (1996). They examine the effect of the fraction of women eligible for Medicaid on birthweight outcomes. To instrument for the state-year fraction of women eligible for Medicaid, they simulate the fraction eligible based on a random draw of women in the U.S. and each state-year s Medicaid eligibility rules. Suppose when economic conditions fall below the nation s average, more people are el- 21

22 igible for Medicaid, but before the downturn, individuals who are newly Medicaid eligible had standard healthcare. Then, the increase in the measure of treatment, D, for this reason should have no effect on birthweight (assuming standard healthcare and Medicaid are perfect substitutes). Because Z is the relevant measure of the treatment, using Z as the treatment measure will estimate an average treatment effect of increased Medicaid eligibility. If a Wald estimator is used instead, with Z as the instrument, we know based on the analysis in previous subsections, that the parameter will be biased upwards in general. When Z and D are continuous as they are in this example, a causal treatment effect cannot be obtained when this Wald estimator is used because effectively Z would need to be a trivial function of D for all individuals, because D changes for any incremental shift in the endogenous variable economic conditions. If the definition of treatment were changed to be discrete say hi and low Medicaid eligibility then an FBATE-like parameter would emerge if Z were a trivial function of D for the subpopulations in which economic conditions induced Z D. When the conditions for FBATE are satisfied, the estimated parameter is not informative about the subpopulations that contribute to endogenous selection. Suppose instead that a decline in economic conditions makes individuals Medicaid eligible who previously didn t have any healthcare. Then, the concerns raised in this paper no longer apply because D is the relevant measure of treatment and a causal average treatment effect will be obtained when the simulated instrument Z is used as an instrument. Note that we are imposing that the response by the groups identified by Z (those eligible because of legislative changes) is the same as the groups only captured in D (those eligible because of an economic downturn in the state); we cannot, from this exercise, learn anything about how the latter group responds, in particular. If we do, the Wald estimates are not valid. 22

23 3 So What Do These Parameters Tell us? This section examines particular reasons why individuals may or may not cross tax bracket lines as part of their response and answers, for each of these cases, what the ITT and causal ATE parameters obtained in the last section tell us about the underlying structural parameters of interest. Section 3.1 examines a series of cases in which no optimization frictions are present and Section 3.2 focuses on the case of a tax kink with optimization frictions. We recognize that there may be other issues that prevent us from identifying the structural parameter in these contexts that do not directly pertain to the discussion in this paper (e.g. Kopczuk, 2005) and are thus not addressed here. 3.1 Tax Kinks, Tax Notches, and Germany: No Optimization Frictions Without optimization frictions, for a single marginal tax change on a convex piece-wise linear budget set that includes only tax kinks, no one crosses tax bracket lines in response to tax rate changes. 16 Take, for example, the reform depicted in Figure 1. This result is predicted by economic theory because, if individuals preferred to be in the other tax bracket, they would have chosen to locate there in the period prior to the tax reform as well. As a result, both measures of treatment are identical and ε IT T = ε F BAT E. There are more complex tax reforms where more than one tax kink is introduced or removed that alters this discussion slightly. For example, consider the case of OBRA93, in which two tax brackets at the top of the income distribution were introduced. The solid green line in Figure 2 depicts the available budget set before the tax reform and the dashed yellow line depicts the same after the tax reform. Based on economic theory, we expect individuals who will be in the top tax bracket after the reform (above k 2 ) based on their income in period 1 will respond by either staying in the top bracket or moving into the other 16 We do not consider concave budget sets because we cannot recover a structural parameter in this setting, regardless of the measure of treatment. 23

24 Figure 2: Bracket Expansion Y- T(Y) A U A U B U B 1- τ 1 1- τ t2 B 1- τ c1 =1- τ c2 k newly introduced bracket just below (between k and k 2 ). The latter response is depicted in Figure 2; before the tax reform, the individual s optimal location is at point A, above k 2, and after the tax reform, the individual s optimal choice is at point B, between kink points k 2 Y k and k 2. This individual would exhibit the same behavioral response if the tax change between k and k 2 were imposed above k 2 as well. This is one of the rare cases in which we prefer to define the tax rate period by period because individuals who respond by moving into the lower tax bracket for this reason should only be assigned the smaller tax change. For a valid instrument, the ITT estimate will always bound the structural parameter from below because it will assign individuals, on average, tax changes that were higher than those they actually faced. In contrast, suppose we started out with three tax brackets and they are collapsed into one bracket as part of the tax reform (in the same spirit, but more extreme than TRA86). Now, both period 1 and period by period tax rates capture the relevant tax change (because there is only one bracket after the reform). Now, consider a case in which there is a tax reform that introduces a higher tax rate above the kink k in the form of a tax notch, as depicted in Figure 3; again, the budget set before the tax reform is given by the solid green line and the budget set after the tax reform is given by the dashed yellow line. What makes this figure different from Figure 1 is that 24